How do I choose research problems to work on?

I often get this question, as I’m sure many other researchers do: how do you choose which research problems you want to work on? Bassam Bamieh gave a nice answer to this question on the latest episode of the inControl podcast (which I highly recommend, by the way). He said that there are two common approaches to this: one is to be driven by a specific important problem (often one arising in an application) and keep trying various methods to solve this problem; another is to have a preferred set of tools and keep applying them to various problems (which is like having a hammer and looking for nails).

As I was listening to Bassam’s explanation, I was thinking that I belong to neither of these two camps. It’s actually a bit difficult to explain how I go about selecting research projects, and this is what this post is about. I may be somewhat closer to the second way of thinking, in the sense that I’m more likely to be motivated by a solution method than by a problem itself. But I don’t get very excited about applying the same set of techniques over and over again. When getting started on a new project, it is important for me to see novelty in it. And it’s not just about novelty; it’s also about beauty, or at least elegance. What I really enjoy is seeing a nice solution or approach to a problem, one that I haven’t seen before and that appeals to my mathematical taste.

I want to stress that for me to appreciate a mathematical concept or technique, it doesn’t necessarily need to be tied to an original research contribution that I’m trying to make. A concept or idea may not be new—it doesn’t matter, as long as it’s new to me. I derive a lot of pleasure from learning beautiful mathematical constructions and results when reading papers and books written by other people, and they don’t need to be related to my own research. Even an elegant solution to a high-school-level math problem can leave a lasting impression. (I have two teenage children, so I think about elementary math problems, puzzles, etc. quite regularly.) Occasionally, though, this feeling of excitement and delight appears when I do research, and it is those moments that help me formulate new research problems and directions.

I suppose I should give a few examples to illustrate and better explain this process. When I was starting my postdoc, I learned that switching between stable linear systems may lead to instability, but that this doesn’t happen if the individual matrices defining the switched system commute with each other. This sparked my long-lasting interest in developing stability criteria for switched systems based on commutation relations (as I explain in much more detail in this recent article, which recounts several other similar moments of inspiration). As another example, at the 2003 CDC in Maui I was presenting my work on quantized feedback systems, and after my talk Dragan Nesic came up to me and suggested that my results could be alternatively derived using small-gain theorems. This idea led to a beautiful and completely new (for me) way of analyzing control algorithms that I have been developing and studying for several years prior to that. It also motivated a general approach to stability analysis of hybrid systems based on small-gain theorems (whose development can be traced from our early and quite accessible 2005 CDC paper to a much more comprehensive 2014 TAC paper). As a much more recent example, at the 2018 CDC in Miami Beach I was presenting our work with Xiaobin Gao and Tamer Başar on stability of slowly time-varying and switched systems. At the end of the talk, someone from the audience asked me what happens when fast variation or switching is also present in the system. I hadn’t thought about this issue and wasn’t able to give a coherent answer on the spot. But later Hyungbo Shim, who also attended my talk and heard the question, told me that he had done some work on averaging for systems with slow and fast time variation, which he thought could be combined with our approach to treat systems where both slow and fast switching and time variation are present. Hyungbo and I decided to join efforts and work this out, and we now have several papers published or in preparation on this topic (one of which he presented just last week at the 2024 HSCC).

I think these examples make it clear that I don’t really have a systematic method for finding good research problems; instead, good research problems occasionally find me, usually when I talk to other people or study their work. But the process is not completely random, as I do have certain criteria that help me decide which ideas to pursue and which ones to discard. An interesting additional observation is that many of the interactions and encounters that turn out to be useful are not planned in advance—which is why it’s very important to have in-person meetings. When our conferences went online during Covid, I felt very uninspired and could not imagine that our field would survive in that mode for very long. I’m able to work quite well remotely on an already existing project using Zoom and email, but that initial spark of inspiration tends to come only during face-to-face conversations (and still only very rarely).

Of course, other people have very different approaches to finding good research problems to work on. I hope you find one that works for you and brings you joy.

Commutation relations and stability of switched systems: a personal history

I recently wrote an expository article presenting an overview of research, conducted mostly between the mid-1990s and late 2000s, that explores a link between commutation relations among a family of asymptotically stable vector fields and stability properties of the switched system that these vector fields generate. This topic is viewed through the lens of my own involvement with it, by interspersing explanations of technical developments with personal reminiscences and anecdotes. You can find the full text here.

Large number of publications slows down progress

I recently attended an informative webinar by Johan Chu, based on this paper in PNAS. Copying from the authors’ significance statement for this paper: “The size of scientific fields may impede the rise of new ideas. Examining 1.8 billion citations among 90 million papers across 241 subjects, we find a deluge of papers does not lead to turnover of central ideas in a field, but rather to ossification of canon. Scholars in fields where many papers are published annually face difficulty getting published, read, and cited unless their work references already widely cited articles. New papers containing potentially important contributions cannot garner field-wide attention through gradual processes of diffusion. These findings suggest fundamental progress may be stymied if quantitative growth of scientific endeavors—in number of scientists, institutes, and papers—is not balanced by structures fostering disruptive scholarship and focusing attention on novel ideas.”

Plagiarism at integrity meeting

An awesome piece of news from Science (Jan 18, 2019):

Researchers studying integrity might be expected to be full of that rare quality. That’s why organizers of the sixth World Conference on Research Integrity, to be held in Hong Kong, China, in June, were surprised to receive an abstract that was, instead, full of apparent plagiarism. After combing through all 430 submissions, they discovered 11 additional cases of suspected plagiarism. When they reached out to the authors of the abstracts—two of which, ironically, were about plagiarism—six didn’t respond, one withdrew their submission, one blamed staff, and two said they had permission to use each other’s work. Only two gave “acceptable” explanations, the organizers reported last week on the Retraction Watch blog.

What are we optimizing: short-term sum or long-term max?

Optimizing some utility function is at the heart of many human activities and processes occurring in nature. Engineering designs often aim to achieve or approximate some optimal performance, while figuring out the right utility function is a major first step towards explaining the behavior of a complex system. Here I would like to apply this principle to try to accomplish a goal that is both philosophical and practical: to better understand how we do research and go about related professional tasks.

The current academic environment, at least in engineering departments in the United States, encourages faculty members to publish many papers, raise a lot of research funds, graduate many students, and in general to be “active,” “productive,” “industrious,” “prolific,” etc. The system rewards such individuals by granting them promotion and tenure, giving them salary raises and awards, and placing them in positions of prominence at their institutions and professional societies. If we try to imagine a utility function that this kind of behavior optimizes, we realize that it has two important features. First, this is short-term optimization. Indeed, salary raises are typically based on one’s performance over the past year; the time horizon for promotion and tenure decisions is only slightly larger, typically around 5 years or less. Second, since each additional paper published, research grant awarded, and dissertation supervised counts towards the overall goal, this short-term utility function takes the form of a sum. With some effort, it can be made into a weighted sum where, for example, publications in top-tier journals are considered more important. Still, such utility functions unfortunately favor short-term gains for the faculty members themselves (and their institutions) over long-term benefits that their work brings to the research community and the society at large.

On the other hand, if we examine long-term impact over several decades or an entire career, a very different picture emerges. When we assess someone’s lifetime achievements, things like the total amount of research funding that this person has raised will probably not even cross our mind. If the person has published several hundred papers, we might be impressed, but most likely only a handful of these papers will remain relevant today. The most important questions that we will ask are: What mark has this person left on the field? Has he/she written a paper or a book, or developed a concept or a technique, that still shapes the way people think? In other words, only the most significant contributions count in the long run. In our optimization setting, this means that the long-term utility function computes a maximum (instead of a sum). There have been some true luminaries who managed to make several contributions of lasting value. However, most of us would be lucky to leave behind one piece of work that will outlive us. The sad truth is that a vast majority of things that we are so preoccupied with will soon be forgotten.

The two forms of utility functions described above—the short-term sum and the long-term max—lead to very different, even conflicting, optimal strategies. The path to increasing the sum is clear: work harder, grow your research group, produce more results. The best way to increase the max is somewhat less obvious, especially since it is difficult to predict which ideas will end up having the most lasting impact; however, it almost certainly involves focusing on fewer things and doing them better, and in general holding ourselves and our students to a higher standard. Of course, in reality we need to work with some convex combination of the two utility functions. Few of us can afford to completely ignore day-to-day pressures or annual performance evaluations. At the same time, I want to believe that most of us do care about the long-term value of the work we are doing as researchers and educators. I think it would be good for all of us to think carefully about the weights that we assign to each of these two components in the overall utility function. In my own opinion, we should not be afraid to increase the weight of our own long-term component, and we should also look for ways to encourage other people to do the same. If we do this, we will all be rewarded in the long run.

Some tips for writing a good paper

If you are a student or a young researcher beginning to write a technical paper, you may find yourself in a difficult position: most likely you have received little or no specific training in how to write well, yet your paper will be the main outcome of your work by which other people will judge you. On this page I’m offering a few general tips, compiled from personal experience, which you might find helpful to consider.

  • First of all, ask yourself whether this paper is worth writing. A good paper should contain new and technically correct results which solve a challenging and well-motivated problem. Will your paper meet all of these criteria? If not, maybe you should postpone the writing and return to the research. Conference deadlines and other such forms of peer pressure are poor excuses, and disappointed readers will be unlikely to take them into account.
  • Before you actually start typing, take the time to think carefully about what you’re going to write. What will be the main message of your paper? Can you clearly visualize the whole paper in your head? Have you decided on the best section structure? If you sit down in front of a computer too early, you’ll end up wasting time. A similar suggestion applies if you get stuck in the middle of writing: get up and take a walk, and don’t resume writing until it becomes clear to you how to proceed.
  • Do not postpone working on a paper until you are no longer excited about the results and have moved on to other things. If the technical content of the paper is still fresh in your mind, writing the text will come more naturally to you and you’ll produce a better paper with less effort. Avoid the common practice of putting a rough draft aside to polish it later, because returning to it will be painful. Careful writing also helps uncover errors and gaps in your reasoning.
  • Writing a paper is a culmination of several months of work, during which you have thought about certain concepts and ideas until your brain became very accustomed to them. Many aspects of your problem which used to be fuzzy have gradually become clear to you, and it is easy to forget the steps that you struggled with. The readers weren’t there with you through this process, though, and this is something you need to constantly keep in mind as you are writing.
  • An important choice to make is regarding the level of generality at which you are going to present your results. The context in which you originally developed your ideas was probably somewhat specific, but they will have more value if cast in a more general conceptual framework. However, if you go too far in this direction, your results may start to look impenetrable to all but the most sophisticated readers. This problem can to some extent be mitigated by giving very specific examples.
  • Motivating the reader doesn’t end with the introduction. Remember that most readers will read your paper only if they want to, not because they have to. So, you have to provide continual motivation for them to keep reading. For example, it is usually not a good idea to start a long calculation that will eventually lead to an important result. It is better to first state the result, explain why it’s important, and then give the calculations required to prove it.
  • The complexity of your writing should be compatible with your English ability. For many of us, English is not the native language. Only use a fancy word or a complicated grammatical construction if you feel confident that you are using it correctly. Otherwise, substitute it with something simpler. You should be in control of the words that you’re writing, not the other way around. And remember that many of your readers won’t be native English speakers either.
  • It is absolutely necessary to print a hard copy for proofreading, preferably after a break and away from the computer. If you’re looking at the screen to check what you’ve just written, many mistakes will go unnoticed because your brain will automatically substitute what you wrote with what you intended to write. It is also easier to see the “big picture” when you’re holding the page in your hands.
  • Learn to be self-critical. Ask yourself not whether what you wrote is good enough, but whether there is any way to further improve it. No matter how much you try, other people will still criticize some aspects of your paper, but at least you’ll be able to say that you did your best. On the other hand, if people see that your writing is sloppy, they will assume that your research is sloppy as well.
  • Remember that you are also writing for yourself, because you will be frequently revisiting your papers in your future work. Getting stuck while trying to follow your own paper is very frustrating (and there is nobody to ask for help). This is another motivation for writing clearly and not covering nontrivial steps with phrases like “it is easy to see that…”
  • Be responsive to reviewers’ comments. Don’t be combative. If a reviewer misunderstood something in your paper, chances are that many readers will misunderstand it as well. Use this feedback to improve your paper. Of course, this doesn’t mean that you should make changes that go against your own taste and judgment just to satisfy the reviewers.
  • It is certainly helpful to read books, articles, and online resources about good writing practices. Papers that you read for your research are also a great resource: while reading them, carefully note what you like and don’t like. Just remember that everyone has their own writing style and not all advice will work for you. This is of course also true of the advice given on this page.

How much do professors work?

Outside academia, it is commonly underestimated how demanding a university professor’s job is. People often just think of the number of teaching hours per week – which is like estimating the workload of a musician or an actor only by the time spent on stage – and are not aware of how many other tasks professors must handle at the same time. An incomplete list of these tasks is given below. The amount of time spent on each one varies widely across different institutions and disciplines and is very hard to estimate, so this is not attempted here.


For each course:

  • Select a textbook, learn/refresh the material, prepare lectures (at least 2 hours of preparation for each 1 hour of lecturing)
  • Deliver lectures
  • Hold office hours
  • Answer students’ emails
  • Prepare homework and exams
  • Supervise the work of lab and homework TAs
  • Grade exams and other assignments
  • Assign final grades
  • In some cases, eventually develop lecture notes into a textbook


For each research project:

  • Come up with an idea
  • Read relevant literature and talk to experts
  • Often, get stuck and return to the first step
  • Develop results
  • Write a conference paper
  • Prepare a talk
  • Travel to a conference/workshop to present it
  • Write a journal paper
  • Revise it (possibly several times) in response to referee comments
  • Travel to other universities to present and discuss the work
  • In some cases, eventually develop research results into a book

Fundraising and student supervision

For each research project:

  • Come up with an idea
  • Write a research proposal to get funding
  • Funding often denied, return to the first step
  • Hire a graduate student to work on the project
  • Train the student to do research, write papers, and present the work
  • Write regular progress reports to the funding agency
  • In some cases, travel to personally report to the program manager


  • Serve on various university committees
  • Serve on doctoral committees of graduate students
  • Review other people’s papers and proposals
  • Serve on journal editorial boards and conference organizing and program committees
  • Write recommendation letters for students and colleagues
  • Participate in the hiring and mentoring of new faculty


  • Respond to email
  • Attend seminars
  • Make preparations for trips (book flights, hotels, etc.)
  • Prepare documents for internal promotion and tenure
  • Maintain a website (and maybe a blog like this one)

Is an academic job right for you?

An academic job, like any other creative occupation, is different from most “usual” jobs in several key aspects. See if you can decide which scenario appeals more to you.

1. The place of work in your life:
A. You want to have a job that’s interesting enough so that you’ll want to think about it almost all the time.
B. You want to have a job that you won’t have to think about when you come home.

2. Your preferred thinking mode:
A. You enjoy thinking slowly and deeply about things.
B. You enjoy making critical real-time decisions.

3. The impact of your work:
A. You like to work on things that may have broad long-term impact.
B. You like to see immediate and clear results of your work.

4. Your independence:
A. You want to be your own boss and decide what you want to work on.
B. You want to have clear structure imposed on you so you always know what you need to do.

5. Your colleagues:
A. You enjoy it when many people around you are smarter than you.
B. You enjoy being smarter than most people around you.

6. Your salary:
A. You don’t care if other people with your education level or lower make more money than you do, as long as you’re paid adequately.
B. You want to make as much money as possible given your level of education and abilities.

If you picked A in most of the above categories, then an academic job might be right for you.

Hello and welcome!

Hello and welcome to my newly started blog. My name is Daniel Liberzon, I am a professor doing research in engineering and applied mathematics (control systems), and from time to time I write down some thoughts about research and academic life in general. I will start by posting here some things already posted earlier on my homepage.